The **design of experiments** (**DOE**, **DOX**, or **experimental design**) is the design of any task that aims to describe or explain the variation of information under conditions that are hypothesized to reflect the variation. The term is generally associated with true experiments in which the design introduces conditions that directly affect the variation, but may also refer to the design of quasi-experiments, in which natural conditions that influence the variation are selected for observation.

## Contents

- Systematic clinical trials
- Statistical experiments following Charles S Peirce
- Randomized experiments
- Optimal designs for regression models
- Sequences of experiments
- Fishers principles
- Example
- Avoiding false positives
- Discussion topics when setting up an experimental design
- Causal attributions
- Statistical control
- Experimental designs after Fisher
- Human participant constraints
- References

In its simplest form, an experiment aims at predicting the outcome by introducing a change of the preconditions, which is reflected in a variable called the predictor (independent). The change in the predictor is generally hypothesized to result in a change in the second variable, hence called the outcome (dependent) variable. Experimental design involves not only the selection of suitable predictors and outcomes, but planning the delivery of the experiment under statistically optimal conditions given the constraints of available resources.

Main concerns in experimental design include the establishment of validity, reliability, and replicability. For example, these concerns can be partially addressed by carefully choosing the predictor, reducing the risk of measurement error, and ensuring that the documentation of the method is sufficiently detailed. Related concerns include achieving appropriate levels of statistical power and sensitivity.

Correctly designed experiments advance knowledge in the natural and social sciences and engineering. Other applications include marketing and policy making.

## Systematic clinical trials

In 1747, while serving as surgeon on HMS *Salisbury*, James Lind carried out a systematic clinical trial to compare remedies for scurvy. This systematic clinical trial constitutes a type of DOE.

Lind selected 12 men from the ship, all suffering from scurvy. Lind limited his subjects to men who "were as similar as I could have them," that is, he provided strict entry requirements to reduce extraneous variation. He divided them into six pairs, giving each pair different supplements to their basic diet for two weeks. The treatments were all remedies that had been proposed:

The citrus treatment stopped after six days when they ran out of fruit, but by that time one sailor was fit for duty while the other had almost recovered. Apart from that, only group one (cider) showed some effect of its treatment. The remainder of the crew presumably served as a control, but Lind did not report results from any control (untreated) group.

## Statistical experiments, following Charles S. Peirce

A theory of statistical inference was developed by Charles S. Peirce in "Illustrations of the Logic of Science" (1877–1878) and "A Theory of Probable Inference" (1883), two publications that emphasized the importance of randomization-based inference in statistics.

## Randomized experiments

Charles S. Peirce randomly assigned volunteers to a blinded, repeated-measures design to evaluate their ability to discriminate weights. Peirce's experiment inspired other researchers in psychology and education, which developed a research tradition of randomized experiments in laboratories and specialized textbooks in the 1800s.

## Optimal designs for regression models

Charles S. Peirce also contributed the first English-language publication on an optimal design for regression models in 1876. A pioneering optimal design for polynomial regression was suggested by Gergonne in 1815. In 1918 Kirstine Smith published optimal designs for polynomials of degree six (and less).

## Sequences of experiments

The use of a sequence of experiments, where the design of each may depend on the results of previous experiments, including the possible decision to stop experimenting, is within the scope of Sequential analysis, a field that was pioneered by Abraham Wald in the context of sequential tests of statistical hypotheses. Herman Chernoff wrote an overview of optimal sequential designs, while adaptive designs have been surveyed by S. Zacks. One specific type of sequential design is the "two-armed bandit", generalized to the multi-armed bandit, on which early work was done by Herbert Robbins in 1952.

## Fisher's principles

A methodology for designing experiments was proposed by Ronald Fisher, in his innovative books: *The Arrangement of Field Experiments* (1926) and *The Design of Experiments* (1935). Much of his pioneering work dealt with agricultural applications of statistical methods. As a mundane example, he described how to test the lady tasting tea hypothesis, that a certain lady could distinguish by flavour alone whether the milk or the tea was first placed in the cup. These methods have been broadly adapted in the physical and social sciences, are still used in agricultural engineering and differ from the design and analysis of computer experiments.

*T*treatments and

*T*– 1 orthogonal contrasts, all the information that can be captured from the experiment is obtainable from the set of contrasts.

## Example

This example is attributed to Harold Hotelling. It conveys some of the flavor of those aspects of the subject that involve combinatorial designs.

Weights of eight objects are measured using a pan balance and set of standard weights. Each weighing measures the weight difference between objects in the left pan vs. any objects in the right pan by adding calibrated weights to the lighter pan until the balance is in equilibrium. Each measurement has a random error. The average error is zero; the standard deviations of the probability distribution of the errors is the same number σ on different weighings; errors on different weighings are independent. Denote the true weights by

We consider two different experiments:

- Weigh each object in one pan, with the other pan empty. Let
*X*_{i}be the measured weight of the object, for*i*= 1, ..., 8. - Do the eight weighings according to the following schedule and let
*Y*_{i}be the measured difference for*i*= 1, ..., 8:

_{1}is Similar estimates can be found for the weights of the other items. For example

The question of design of experiments is: which experiment is better?

The variance of the estimate *X*_{1} of θ_{1} is σ^{2} if we use the first experiment. But if we use the second experiment, the variance of the estimate given above is σ^{2}/8. Thus the second experiment gives us 8 times as much precision for the estimate of a single item, and estimates all items simultaneously, with the same precision. What the second experiment achieves with eight would require 64 weighings if the items are weighed separately. However, note that the estimates for the items obtained in the second experiment have errors that correlate with each other.

Many problems of the design of experiments involve combinatorial designs, as in this example and others.

## Avoiding false positives

False positive conclusions, often resulting from the pressure to publish or the author's own confirmation bias, are an inherent hazard in many fields. A good way to prevent biases potentially leading to false positives in the data collection phase is to use a double-blind design. When a double-blind design is used, participants are randomly assigned to experimental groups but the researcher is unaware of what participants belong to which group. Therefore, the researcher can not affect the participants' response to the intervention. Experimental designs with undisclosed degrees of freedom are a problem. This can lead to conscious or unconscious "p-hacking": trying multiple things until you get the desired result. It typically involves the manipulation - perhaps unconsciously - of the process of statistical analysis and the degrees of freedom until they return a figure below the p<.05 level of statistical significance. So the design of the experiment should include a clear statement proposing the analyses to be undertaken. P-hacking can be prevented by preregistering researches, in which researchers have to send their data analysis plan to the journal they wish to publish their paper in before they even start their data collection, so no data mining is possible (https://osf.io). Another way to prevent this is taking the double-blind design to the data-analysis phase, where the data are sent to a data-analyst unrelated to the research who scrambles up the data so there is no way to know which participants belong to before they are potentially taken away as outliers.

Clear and complete documentation of the experimental methodology is also important in order to support replication of results.

## Discussion topics when setting up an experimental design

An experimental design or randomized clinical trial requires careful consideration of several factors before actually doing the experiment. An experimental design is the laying out of a detailed experimental plan in advance of doing the experiment. Some of the following topics have already been discussed in the principles of experimental design section:

- How many factors does the design have? and are the levels of these factors fixed or random?
- Are control conditions needed, and what should they be?
- Manipulation checks; did the manipulation really work?
- What are the background variables?
- What is the sample size. How many units must be collected for the experiment to be generalisable and have enough power?
- What is the relevance of interactions between factors?
- What is the influence of delayed effects of substantive factors on outcomes?
- How do response shifts affect self-report measures?
- How feasible is repeated administration of the same measurement instruments to the same units at different occasions, with a post-test and follow-up tests?
- What about using a proxy pretest?
- Are there lurking variables?
- Should the client/patient, researcher or even the analyst of the data be blind to conditions?
- What is the feasibility of subsequent application of different conditions to the same units?
- How many of each control and noise factors should be taken into account?

The independent variable of a study often has many levels or different groups. In a true experiment, researchers can have an experimental group, which is where their intervention testing the hypothesis is implemented, and a control group, which has all the same element as the experimental group, without the interventional element. Thus, when everything else except for one intervention is held constant, researchers can certify with some certainty that this one element is what caused the observed change. In some instances, having a control group is not ethical. This is sometimes solved using two different experimental groups. In some cases, independent variables cannot be manipulated, for example when testing the difference between two groups who have a different disease, or testing the difference between genders (obviously variables that would be hard or unethical to assign participants to). In these cases, a quasi-experimental design may be used.

## Causal attributions

In the pure experimental design, the independent (predictor) variable is manipulated by the researcher - that is - every participant of the research is chosen randomly from the population, and each participant chosen is assigned randomly to conditions of the independent variable. Only when this is done is it possible to certify with high probability that the reason for the differences in the outcome variables are caused by the different conditions. Therefore, researchers should choose the experimental design over other design types whenever possible. However, the nature of the independent variable does not always allow for manipulation. In those cases, researchers must be aware of not certifying about causal attribution when their design doesn't allow for it. For example, in observational designs, participants are not assigned randomly to conditions, and so if there are differences found in outcome variables between conditions, it is likely that there is something other than the differences between the conditions that causes the differences in outcomes, that is - a third variable. The same goes for studies with correlational design. (Adér & Mellenbergh, 2008).

## Statistical control

It is best that a process be in reasonable statistical control prior to conducting designed experiments. When this is not possible, proper blocking, replication, and randomization allow for the careful conduct of designed experiments. To control for nuisance variables, researchers institute **control checks** as additional measures. Investigators should ensure that uncontrolled influences (e.g., source credibility perception) do not skew the findings of the study. A manipulation check is one example of a control check. Manipulation checks allow investigators to isolate the chief variables to strengthen support that these variables are operating as planned.

One of the most important requirements of experimental research designs is the necessity of eliminating the effects of spurious, intervening, and antecedent variables. In the most basic model, cause (X) leads to effect (Y). But there could be a third variable (Z) that influences (Y), and X might not be the true cause at all. Z is said to be a spurious variable and must be controlled for. The same is true for intervening variables (a variable in between the supposed cause (X) and the effect (Y)), and anteceding variables (a variable prior to the supposed cause (X) that is the true cause). When a third variable is involved and has not been controlled for, the relation is said to be a zero order relationship. In most practical applications of experimental research designs there are several causes (X1, X2, X3). In most designs, only one of these causes is manipulated at a time.

## Experimental designs after Fisher

Some efficient designs for estimating several main effects were found independently and in near succession by Raj Chandra Bose and K. Kishen in 1940 at the Indian Statistical Institute, but remained little known until the Plackett-Burman designs were published in *Biometrika* in 1946. About the same time, C. R. Rao introduced the concepts of orthogonal arrays as experimental designs. This concept played a central role in the development of Taguchi methods by Genichi Taguchi, which took place during his visit to Indian Statistical Institute in early 1950s. His methods were successfully applied and adopted by Japanese and Indian industries and subsequently were also embraced by US industry albeit with some reservations.

In 1950, Gertrude Mary Cox and William Gemmell Cochran published the book *Experimental Designs,* which became the major reference work on the design of experiments for statisticians for years afterwards.

Developments of the theory of linear models have encompassed and surpassed the cases that concerned early writers. Today, the theory rests on advanced topics in linear algebra, algebra and combinatorics.

As with other branches of statistics, experimental design is pursued using both frequentist and Bayesian approaches: In evaluating statistical procedures like experimental designs, frequentist statistics studies the sampling distribution while Bayesian statistics updates a probability distribution on the parameter space.

Some important contributors to the field of experimental designs are C. S. Peirce, R. A. Fisher, F. Yates, C. R. Rao, R. C. Bose, J. N. Srivastava, Shrikhande S. S., D. Raghavarao, W. G. Cochran, O. Kempthorne, W. T. Federer, V. V. Fedorov, A. S. Hedayat, J. A. Nelder, R. A. Bailey, J. Kiefer, W. J. Studden, A. Pázman, F. Pukelsheim, D. R. Cox, H. P. Wynn, A. C. Atkinson, G. E. P. Box and G. Taguchi. The textbooks of D. Montgomery and R. Myers have reached generations of students and practitioners. Some discussion of experimental design in the context of system identification (model building for static or dynamic models) is given in and.

## Human participant constraints

Laws and ethical considerations preclude some carefully designed experiments with human subjects. Legal constraints are dependent on jurisdiction. Constraints may involve institutional review boards, informed consent and confidentiality affecting both clinical (medical) trials and behavioral and social science experiments. In the field of toxicology, for example, experimentation is performed on laboratory *animals* with the goal of defining safe exposure limits for *humans*. Balancing the constraints are views from the medical field. Regarding the randomization of patients, "... if no one knows which therapy is better, there is no ethical imperative to use one therapy or another." (p 380) Regarding experimental design, "...it is clearly not ethical to place subjects at risk to collect data in a poorly designed study when this situation can be easily avoided...". (p 393)